Low-degree mantle melting controls the deep seismicity and explosive volcanism of the Gakkel Ridge

The world’s strongest known spreading-related seismicity swarm occurred in 1999 in a segment of the Gakkel Ridge located at 85°E as a consequence of an effusive-explosive submarine volcanic eruption. The data of a seismic network deployed on ice floes were used to locate hundreds of local earthquakes down to ∼25 km depth and to build a seismic tomography model under the volcanic area. Here we show the seismicity and the distribution of seismic velocities together with the 3D magmatic-thermomechanical numerical model, which demonstrate how a magma reservoir under the Gakkel Ridge may form, rise and trigger volcanic eruptions in the rift valley. The ultraslow spreading rates with low mantle potential temperatures appear to be a critical factor in the production of volatile-rich, low-degree mantle melts that are focused toward the magma reservoirs within narrow magmatic sections. The degassing of these melts is the main cause of the explosive submarine eruptions.

That said…the quality of the presentation can be improved, the English is poor in places, the understanding of the broader picture of oceanic volcanism has some misconceptions, the detailed interpretation of the seismic data in terms of lithologies present is surely uncertain, and the results of the modeling have aspects that are not consistent with some of what is observed along the Gakkel Ridge. None of these flaws are fatal, but if they were fixed I think a much improved paper would be possible. And in my view a more appropriate conclusion at the end would be to note that this is a first step with a lot of future potential.
There is one aspect that really needs to be dealt with, which comes from the geochemistry. The authors ignore the geochemical data that is available for the volcanic products of the explosive eruption they are modeling. CO2 contents are known for these magmas, and the degassing depths can be accurately determined. They are not consistent with the model proposed, so the authors need to think how to modify the model so they do not violate the geochemical constraints, and they certainly need to reference and discuss the geochemical data that are directly pertinent.
My bottom line would be to recommend major revisions and a second round of review. There is a lot of interesting work that has been done here that should be in the literature.
I also would recommend that the authors need to be more generous to Sohn et al. Yes, the current work has a much more comprehensive approach, and the seismic and numerical results are far beyond what Sohn et al did. But the model they come up with is similar to what the earlier paper suggested. I know it is hard to write sentences like "our new interpretation of the seismic data coupled with numerical modeling leads to conclusions consistent with earlier suggestions." But that is the case here. The paper only references Sohn for the volcanological observations and inferred high CO2 content. But Sohn et al. said: "These results provide a new perspective for interpreting the 1999 seismic swarm and volcanic event at the 85° E site. The seismic swarm began with extensional events, but after three months the earthquakes changed to sources with large volume changes (implosions) 6 . Large-volumechange events are rare at MORs, but they are consistent with the rapid evacuation of explosive material from a deep-lying magma chamber. The sequence of extensional earthquakes leading up to the implosions may have perturbed the stress field enough to fracture the chamber roof, thereby releasing pressurized magmatic volatiles. Rapid acceleration of decompressing volatiles may have triggered vulcanian explosions during the eruption 3 , consistent with the talus distribution observed on Oden volcano. Multiple episodes of explosive volatile discharge over a prolonged period are required for producing the variations in apparent age and thickness of the deposits we observed, and we note that small-magnitude explosive acoustic signals were detected by local (ice-mounted) seismic networks at the eruption site more than two years after the 1999 seismic swarm 19 . Explosive volatile discharge has clearly been a widespread, and ongoing, process at the 85° E segment.
Our results raise new questions about volatile processes in ultraslow-spreading magmatic systems. More observations will be necessary to determine the ubiquity of pyroclastic activity at ultraslow spreading rates (<15-20 mm yr -1 , full rate), but from first principles there is reason to believe that ultraslow-spreading ridges may be especially conducive to the build-up and explosive discharge of volatile-rich magmatic foams. Long time intervals between eruptions should increase the quantity of volatiles that can be accumulated in a magma chamber, and if the global correlation between spreading rate and magma chamber depth extends to ultraslow rates, then volatile build-up will occur deep within the crust at high storage pressures. Our results add to the growing body of evidence that ultraslow-spreading ridges host unique modes of crustal accretion and tectonic extension 20,21 , and motivate continuing efforts to solve the technical and logistical issues that have impeded scientific access to these unique geological environments." This paper concludes: "Hence, we conclude that 170 ultralow spreading ridges with low mantle potential temperature may not only focus deep rising 171 partially molten asthenosphere towards magma chamber to form narrow magmatic sections, but 172 also subsequently trigger volcanic eruptions in the rift valley due to the very high volatile content 173 in the focused low-degree basaltic melts." Isn't that the same conclusion as Sohn et al? Figure 4 of the present paper is consistent with this view, and the earlier paper also emphasizes that this is likely a consequence of super-slow spreading. So, the present authors have done a lot of novel work, but they might better acknowledge the previous contributions and ideas.

The language
Here is a statement from the first paragraph: "The divergent processes along the spreading centers cause forming the new lithosphere, 32 which fully compensates for lithosphere submerging in subduction and collision zones. All lower density crust. Ocean crust is normally 6km thick. Extents of melting are mostly 8-15%. They cannot be 2% beneath the Gakkel. In that case you would never get crust more than a couple of hundred meters thick.

Seismology
I am not a seismologist, so not qualified to comment on the detailed seismic treatment. But from the outsider's point of view, the interpretation seems inherently problematic because no S waves are received by seismometers sitting on top of the ocean. For this reason the authors have to depend on the P-S wave conversion. While real S-waves can be picked reliably, it is not so clear from the examples given in the appendix that P-S conversion picks are as reliable. The testing they do does not take this uncertainty into account. Furthermore, converting the Vp/"inferred Vs" to melt fraction and detailed lithology is non-unique and quite unconstrained. I hope a seismology expert is engaged to give views on these points.

Modeling
I am not a numerical modeler. The appendix gives a lot of detail about the numerical choices that were made, but some aspects are strange and raise questions. First, the initial condition shown in Figure S6 of a constant 7km crust just does not apply in this region. Do model results depend on that initial condition? If you start with the run after 10ma as the initial condition, what happens? Does that control the faulting that eventually occurs? Second, the 85E volcano is an isolated edifice surrounded by 100km on either side with no apparent volcanism. The modeling results, however, lead to 20km spacing between upwellings. So there appears to be a first order misfit. Third, is there clear geological evidence for a detachment fault in this region (e.g. unroofed lower crust, straited bathymetry, assymetric cross sections)? And yet such a fault seems important for the modeling results and interpretation in the paper.  Figure 4. No magma in the reservoir shown will degas. OK, move the reservoir up a little? No, 3kb is the solubility pressure, and you have to degas from 3-2kb in order to release 40% of the CO2 as gas. You can also calculate degassing paths in VolatileCalc. To get the 14% CO2 the authors propose for an explosive eruption, that gas needs to accumulate at some shallower level, and to have accumulated from a volume of magma that is more than one hundred times the erupted volume, because you do not completely degas the magma. It is also not obvious to me how you trap it. These volumetric contraints also mean that these kinds of eruptions must be rare-they can only be one percent of magma production. That makes generalizations about explosivity and super slow spreading rates a bit difficult.
In any case, the authors cannot avoid the CO2 constraints. There cannot be a deep magma chamber that is the source of the eruptions, because no degassing occurs there. There are also strict limits on the amount of CO2 that can be in the primary magma-you do not get just to gather CO2 from large volumes of asthenosphere and not also gather Ba and Th. And the Ba contents of the erupted rocks are the same as the Gale et al. Average MORB, so the CO2 contents are not particularly elevated, and it is not exceptionally high CO2 in the primary magmas that is the ultimate cause. It also means the source of the eruptions needs to be a holding tank much shallower in the crust. Geochemical conclusions, like what the extent of melting is and how much CO2 there is, are constrained by the geochemical observations from the erupted magmas.
So in view of these considerations the conclusion on lines 128-133 of a magma reservoir that is the source of the eruptions at 10-15km is simply not possible.
One might think in view of these issues that I would suggest the paper be rejected. But that is not my view, because the paper reflects a lot of work and a novel approach that has promise. That alone makes it a worthwhile contribution to the literature. Further work of this kind could make a major contribution to our understanding of ocean ridges.

Charles Langmuir
Harvard University My detailed comments in order are as follows: In main manuscript: Line 46

2.) Please also show histograms of residuals of both P-and SP. The quality of tomographic
results is rather poorly presented.

Rebuttal letter on the revised paper by Ivan Koulakov, Vera Schlindwein, Mingqi Liu, Taras Gerya, Andrey Jakovlev and Alexei Ivanov "Low-degree mantle melting controls deep seismicity and explosive volcanism of the Gakkel Ridge" submitted to Nature Communications (Paper # NCOMMS-21-38084-T)
The author's responses are indicated with -REP:‖ and highlighted with the red color. Line numbering corresponds to the version of the manuscript with tracked changes.

Reviewer 1
This is a useful paper that ties together previous volcanological observations, a new treatment of existing seismic data, and numerical modeling of melt generation and crustal construction.
The authors suggest all of these are consistent with one another, and in combination provide a new understanding of how it is possible to get explosive eruptions at super-slow spreading ridges. It's a nice story, reflects a lot of work, and therefore should be published after revision. As far as being worthy of a Nature journal, my answer is yes, because the combination of these three things is new to me. Maybe it is unique? So even if the results are not definitive, this is an important new approach and contribution. Future work can build upon it. Let's not hold it up too much by complaining about the details.
That said…the quality of the presentation can be improved, the English is poor in places, the understanding of the broader picture of oceanic volcanism has some misconceptions, the detailed interpretation of the seismic data in terms of lithologies present is surely uncertain, and the results of the modeling have aspects that are not consistent with some of what is observed along the Gakkel Ridge. None of these flaws are fatal, but if they were fixed I think a much improved paper would be possible. And in my view a more appropriate conclusion at the end would be to note that this is a first step with a lot of future potential.

REP:
We did our best to follow these recommendations (see our responses below).
There is one aspect that really needs to be dealt with, which comes from the geochemistry. The authors ignore the geochemical data that is available for the volcanic products of the explosive eruption they are modeling. CO2 contents are known for these magmas, and the degassing depths can be accurately determined. They are not consistent with the model proposed, so the authors need to think how to modify the model so they do not violate the geochemical constraints, and they certainly need to reference and discuss the geochemical data that are directly pertinent.

REP:
Our new co-author Alexei Ivanov took care of the geochemical issues and made an important contribution to address the problems mentioned by the reviewer (see our responses below).
My bottom line would be to recommend major revisions and a second round of review. There is a lot of interesting work that has been done here that should be in the literature. I also would recommend that the authors need to be more generous to Sohn et al. Yes, the current work has a much more comprehensive approach, and the seismic and numerical results are far beyond what Sohn et al did. But the model they come up with is similar to what the earlier paper suggested. I know it is hard to write sentences like -our new interpretation of the seismic data coupled with numerical modeling leads to conclusions consistent with earlier suggestions.‖ But that is the case here. The paper only references Sohn for the volcanological observations and inferred high CO2 content. But Sohn et al. said: -These results provide a new perspective for interpreting the 1999 seismic swarm and volcanic event at the 85° E site. The seismic swarm began with extensional events, but after three months the earthquakes changed to sources with large volume changes (implosions)6. Large-volume change events are rare at MORs, but they are consistent with the rapid evacuation of explosive material from a deep-lying magma chamber. The sequence of extensional earthquakes leading up to the implosions may have perturbed the stress field enough to fracture the chamber roof, thereby releasing pressurized magmatic volatiles. Rapid acceleration of decompressing volatiles may have triggered vulcanian explosions during the eruption3, consistent with the talus distribution observed on Oden volcano. Multiple episodes of explosive volatile discharge over a prolonged period are required for producing the variations in apparent age and thickness of the deposits we observed, and we note that small-magnitude explosive acoustic signals were detected by local (ice-mounted) seismic networks at the eruption site more than two years after the 1999 seismic swarm19. Explosive volatile discharge has clearly been a widespread, and ongoing, process at the 85° E segment.
Our results raise new questions about volatile processes in ultraslow-spreading magmatic systems. More observations will be necessary to determine the ubiquity of pyroclastic activity at ultraslow spreading rates (<15-20 mm yr-1, full rate), but from first principles there is reason to believe that ultraslow-spreading ridges may be especially conducive to the build-up and explosive discharge of volatile-rich magmatic foams. Long time intervals between eruptions should increase the quantity of volatiles that can be accumulated in a magma chamber, and if the global correlation between spreading rate and magma chamber depth extends to ultraslow rates, then volatile build-up will occur deep within the crust at high storage pressures. Our results add to the growing body of evidence that ultraslow-spreading ridges host unique modes of crustal accretion and tectonic extension20,21, and motivate continuing efforts to solve the technical and logistical issues that have impeded scientific access to these unique geological environments.‖ This paper concludes: -Hence, we conclude that ultralow spreading ridges with low mantle potential temperature may not only focus deep rising partially molten asthenosphere towards magma chamber to form narrow magmatic sections, but also subsequently trigger volcanic eruptions in the rift valley due to the very high volatile content in the focused low-degree basaltic melts.‖ Isn't that the same conclusion as Sohn et al? Figure 4 of the present paper is consistent with this view, and the earlier paper also emphasizes that this is likely a consequence of super-slow spreading. So, the present authors have done a lot of novel work, but they might better acknowledge the previous contributions and ideas.

REP:
We agree that in many aspects our results are consistent with the concept proposed by Sohn and others. We have highlighted this in some parts of the text (for example in L207-208). However, we slightly disagree that our conclusions completely repeat the statements proposed by Sohn et al. (2008). In the highlighted pieces of text from the Sohn's work, there is discussion about a large amount of volatiles responsible for explosive volcanism in the ultraslow spreading settings. In our work, we do not investigate the volatiles, but mostly use the information about them provided by other authors, including Sohn et al. At the same time, as far as we aware, the previous studies did not find a definitive answer to a question on where this high concentration of volatiles comes from and why such centres of activity focus in narrow sections. Based on seismic tomography, we show for the first time the location of the magma below the spreading centre, and our numerical model provides an explanation of focusing such volatile-rich magma reservoirs in the conditions of relatively cold spreading zone. As far as we know, none of the existing articles considered the origin of volcanism in the Gakkel Ridge in this aspect.

The language
Here is a statement from the first paragraph: -The divergent processes along the spreading centers cause forming the new lithosphere, which fully compensates for lithosphere submerging in subduction and collision zones. All spreading zones are located in deep-water oceanic areas,‖

REP:
We have replaced -All spreading zones‖ with -Most of spreading centres‖. For the first part of the highlighted phrase, we do not understand what is wrong.
Or later: 104 Indeed, the P-wave velocity is more sensitive to the composition and is normally higher in magmas of primitive composition arrived from deeper sources (24). This is a basaltic system, so p-wave velocity will not vary much within the small range of composition.

REP:
We have replaced this statement with: -Indeed, the P-wave velocity is more sensitive to the composition and is normally higher in magmas arrived from the mantle than in crustal rocks (24)‖ (L116-117). Or: 168 an ovoid magma chamber appears with high temperature and high strain rate, which likely reveals strong fluid-melt activity and further interprets the main source of volcanic eruptions occurring.
How can a magma chamber have a strain rate? It is a liquid. I have no idea what line 169 actually means.

REP:
In our numerical model, the lower crustal magma chamber is only partially molten and contains crystal mush rather than pure liquid. We removed mention of strain rate to avoid confusion.
There are many other examples throughout the paper. The numerical supplement seems to be well written. The authors with more facility in written English need to do a major edit to the paper, and also make sure the sentences make sense.

REP:
The English language of our manuscript was checked by professional editors from American Journal Experts.

Ocean ridges
The authors make statements that are just wrong about ocean ridges. Not all ridges are submarine and deep (they are shallow where hot spots are nearby, Iceland is above sea level); there are quite a few segments as deep as the 85E volcano, ridge basalts are not generated by 15-20% melting. Here is the segment depth distribution from Gale et al. 85E is the big yellow symbol. Shallow ridge segments are off scale to the right.
These are mean depths. The actual 85E volcano depth is mostly shallower than 4000m. Super slow spreading ridges encompass a very large range in depth.

REP:
In L59, we replaced -at depths of more than 4000 meters‖ with -at depths of 3700-4000 meters‖, which gives more accurate range for the bottom depth in the volcanic area.
If numerical modeling is giving 15-20% as an average extent of melting, the models need to be revised. The maximum extent of melting gets that high, but mean melt production is approximately the crustal thickness divided by the maximum dry melting depth, corrected for density. Since melting starts at 60km or more, if you melt even 15% you get about 10km of lower density crust. Ocean crust is normally 6km thick. Extents of melting are mostly 8-15%.
They cannot be 2% beneath the Gakkel. In that case you would never get crust more than a couple of hundred meters thick.

REP:
The extent of melting is clarified. In our numerical model, the average extent of melting is about 9-11% (please see the figure below). Higher degree of melting is only characteristic for the model initiation due to the prescribed initial hot temperature profile along the ridge (Fig. S16), which cools down with time and goes toward the colder equilibrium state (Fig. S17).

Distribution of melting degree on mantle markers at both magmatic and amagmatic sections. (a) The extent of melting at magmatic section. (b) The extent of melting at amagmatic section. (c) The extent of melting along the dashed white lines in (a) and (b). The very high extent of melting (red color) in (a) and (b) is caused by the initial thermal configuration.
Seismology I am not a seismologist, so not qualified to comment on the detailed seismic treatment. But from the outsider's point of view, the interpretation seems inherently problematic because no S waves are received by seismometers sitting on top of the ocean. For this reason the authors have to depend on the P-S wave conversion. While real S-waves can be picked reliably, it is not so clear from the examples given in the appendix that P-S conversion picks are as reliable. The testing they do does not take this uncertainty into account. Furthermore, converting the Vp/‖inferred Vs‖ to melt fraction and detailed lithology is non-unique and quite unconstrained. I hope a seismology expert is engaged to give views on these points.

REP:
We have added a paragraph, in which we describe in details how the manual picking of the direct P and converted P-S waves was conducted and how the correctness of the phase identification was tested (L107-123 of Supplementary).
Regarding to the non-uniqueness of interpretation of the derived seismic model in terms of petrological parameters, we admit that this problem cannot be solved quantitatively. However, we note that an interpretation can be proposed based on similarity of seismic structures obtained for a number of other active volcanoes, where multidisciplinary studies provided robust information about magma plumbing systems. We have added a paragraph in the main paper summarizing this issue (L 105-113 of the main paper).

Modeling
I am not a numerical modeler. The appendix gives a lot of detail about the numerical choices that were made, but some aspects are strange and raise questions. First, the initial condition shown in Figure S6 of a constant 7km crust just does not apply in this region. Do model results depend on that initial condition? If you start with the run after 10ma as the initial condition, what happens? Does that control the faulting that eventually occurs?
REP: Explanation of the initial conditions has been extended. With this initially hot symmetrical ridge condition we intended to avoid influence of any initial ridge asymmetry for the model evolution. As the result, ridge asymmetry develops spontaneously from the initially symmetrical configuration upon cooling of the ridge toward the equilibrium thermal state. At the beginning, the initial condition (e.g., thermal configuration and oceanic crust) can indeed affect the model results in term of elevated degree of mantle melting. However, after about 3 Myr, the effect of initial setup in model results becomes negligible.
Second, the 85E volcano is an isolated edifice surrounded by 100km on either side with no apparent volcanism. The modeling results, however, lead to 20km spacing between upwellings. So there appears to be a first order misfit.

REP:
The discussion of modelling results has been extended. The reference model shows about 20 km spacing between upwelling, which is indeed not consistent with the observation. However, through exploring the effect of different spreading rates and mantle potential temperature for the distribution of magmatic segments, we found that reduced spreading rate and lower mantle potential temperature can increase the spacing between upwellings. Thus, if the reduced spreading rate and lower mantle potential temperature are implemented, the larger spacing can be produced. This however does not change the discussed relationship and structure of magmatic vs. amagmatic segments.
Third, is there clear geological evidence for a detachment fault in this region (e.g. unroofed lower crust, straited bathymetry, assymetric cross sections)? And yet such a fault seems important for the modeling results and interpretation in the paper. . Solubility pressure is 3kb, which is the pressure just above the very top of the proposed magma reservoir in Figure 4. No magma in the reservoir shown will degas. OK, move the reservoir up a little? No, 3kb is the solubility pressure, and you have to degas from 3-2kb in order to release 40% of the CO2 as gas. You can also calculate degassing paths in VolatileCalc. To get the 14% CO2 the authors propose for an explosive eruption, that gas needs to accumulate at some shallower level, and to have accumulated from a volume of magma that is more than one hundred times the erupted volume, because you do not completely degas the magma. It is also not obvious to me how you trap it. These volumetric contraints also mean that these kinds of eruptions must be rare-they can only be one percent of magma production. That makes generalizations about explosivity and super slow spreading rates a bit difficult.

REP:
In any case, the authors cannot avoid the CO2 constraints. There cannot be a deep magma chamber that is the source of the eruptions, because no degassing occurs there. There are also strict limits on the amount of CO2 that can be in the primary magma-you do not get just to gather CO2 from large volumes of asthenosphere and not also gather Ba and Th. And the Ba contents of the erupted rocks are the same as the Gale et al. Average MORB, so the CO2 contents are not particularly elevated, and it is not exceptionally high CO2 in the primary magmas that is the ultimate cause. It also means the source of the eruptions needs to be a holding tank much shallower in the crust. Geochemical conclusions, like what the extent of melting is and how much CO2 there is, are constrained by the geochemical observations from the erupted magmas.

REP:
This comment is very useful and allowed us to modify the model in accordance with the published geochemical data of Shaw et al. (2010). Taking CO2 concentrations of 1600 ppm and VolatileCalc we obtain 3.1 kbar saturation pressure which corresponds to the depth of anomaly 2. We have added a paragraph in L260-276 in the main paper and modified Fig. 4 (indicating much shallower depths of degassing).
So in view of these considerations the conclusion on lines 128-133 of a magma reservoir that is the source of the eruptions at 10-15km is simply not possible.
One might think in view of these issues that I would suggest the paper be rejected. But that is not my view, because the paper reflects a lot of work and a novel approach that has promise.
That alone makes it a worthwhile contribution to the literature. Further work of this kind could make a major contribution to our understanding of ocean ridges.

Charles Langmuir
Harvard University Reviewer #2 (Remarks to the Author): Review of -Low-degree mantle melting controls deep seismicity and explosive volcanism of the Gakkel Ridge‖ This manuscript presents the results from coupled seismic and thermo-mechanical modeling analysis carried out beneath the Gakkel Ridge. Some of the data/results build on previous studies, i.e., seismicity, but both the 3D velocity and the thermo-mechanical models are new and shed light on some fundamental processes of magmatic/tectonic accretion at ridges. Both results and interpretation leading to providing a plausible scenario for what causes explosive volcanism and deep seismicity beneath the Gakkel ridge would be of interest for the marine geodynamics and ridge communities at large. Overall, the paper is well-written and the authors make a good job at presenting and discussing their results. I have a few comments though, detailed below, that need clarification before any publication.
My detailed comments in order are as follows: In main manuscript: Line 46 Lines 49-50: is it really a frequent feature? I would tone down on the -frequent‖ and remove it. Some studies show otherwise, i.e., < 18 km depth, e.g., Grevemeyer, I., et al., 2019.

REP:
We have corrected this sentence as -Similarly deep seismicity is observed in a few other centres of slow spreading and is explained by anomalously low temperature beneath the rift axis (13,14,15)‖ (L51-53).

REP: Corrected
Line 60: Why is the authors stating that seismicity reaches 25 km depth when they show on figure 2 (red dots) that some EQs were recorded at 32 km focal depth (which is impressively deep and not discussed)?

REP:
Here we write the phrase: -Robustly resolved seismicity was detected at depths of up to 25 km, which are far below the bottom of the crust (21)‖ (L63-64). This is based on the work of (21), where there is seismicity down to 25 km depth, with a with a few scattered events deeper than that. These results were based on a 1D velocity model initial location. We now consider a 3D velocity model and obtain a few events deeper than 25 km. In the later parts of the article, we will admit that these events appearing at greater depths are less robust, and should be interpreted with prudence (L139).
Lines 114-120: this seismic gap inferred and interpreted as the consequence of crustal rocks being too soft (surface: more fractured and saturated with seawater and in depth: remnant magma pocket), which would prevent accumulation of stresses and generation of seismicity, have been observed in Schlindwein and Schmid's (2016) study of SWIR micro-seismicity. Later, Grevmeyer et al. (2019) analysis of the SWIR dataset indicates that the previously proposed thick aseismic region in the upper lithosphere was -simply a consequence of a model embedded in the hypocenter location procedure that did not include a few 100 m-thickness of unconsolidated sediment‖. They show the strong influence of such layer (and hence the importance of including such layer in models) on the focal depth and apparent seismic gap. Furthermore, because of their very slow spreading rate, ultraslow-ridges are known to have substantial sediment thick layer at the axis and flanks. Was any unconsolidated sediment layer considered in this present study to avoid this bias which would result in having artifacts, i.e., seismic gap and deep seismicity? If not, how can you state that this isn't a bias of not considering such layer and can you provide model results including such layer for comparaison?

REP:
To address this comment, we have added a series of new synthetic tests presented in Figure S8, in which we evaluate a possible role of the upper low-velocity layer on the results of source locations. The results of this test demonstrate that the completely different structures of the upper layer in the rift valley do not dramatically affect the distributions of events. In particular, in the model, there were several shallow events that remained at approximately same depths after recovery, regardless the uppermost structures. Thus, the suggestion about critical effect of sediments on the rift valley on source locations appears to be not valid. We have paragraph with the discussion of this issue in Supplementary in L239-249.
Note also that the layer of soft unconsolidated silica ooze is very special to the site at the SWIR (located beneath the Polar Front and acting as sediment trap) and there it only affected stations in the rift valley. These soft sediments were visible in parasound data and even in seafloor imagery. In the seismicity data, significantly delayed S phases appeared on the stations affected by the soft sediments, but not on the remaining stations outside the central rift valley. At Gakkel Ridge, such a layer of silica ooze has not been observed. Instead there is a thick pile of comparatively consolidated sediments of continental origin covering the rift valley away from the volcanoes. None of the recently refraction seismic studies (Jasmine cruise, AMORE) gave indications for such a layer. Furthermore, we currently process OBS data from a volcanic center at 120°E Gakkel Ridge. No indications for anomalous delays of S phases are visible there. Along Knipovich Ridge, for example, there are no unconsolidated sediments at the surface and we used a similar location routine (comparing different approaches) for an extensive along axis network of seismometers. We observe a) an aseismic upper lithosphere with temperature-controlled boundaries and an onset of seismicity below 10 km depthcomparable to the observation at the SWIR, which by the way persists after dealing carefully with the soft sediment layersee comment to Grevemeyers paper. b) seismicity generally is not recorded from the top 3-4 km below the surface, probably due to the processes discussed herefracturing, presence of sea water etc. In this paper it becomes obvious that in some places there is scattered very shallow seismicity.
We are therefore certain that we see here an aseismic behaviour that is different from the one described in Schlindwein and Schmid and Meier et al. that is related most likely to aseismic deformation of altered mantle material in amagmatic regions. Instead we rather observe a general lack of very shallow seismicity (as in Meier et al.) with some scattered shallow events, that is mostly a result of local surface conditions and potentially the detection threshold of the network for weak, shallow seismicity.
Line 125: here again, a depth of about 25 km is mentioned while they clearly show deeper seismicity (up to 32 km)is the 32 km EQ(s) considered an outlier(s)? If so, it needs to be explicated and discussed.

REP:
We have reformulated this phrase as: -Another feature of the Gakkel Ridge is that its axis line is smooth and almost not dissected by transform faults (10). Such a behavior is only observed on a few other ultra-slow ridges (such as Mohn and Knipovich Ridges), but it appears to be exceptional compared to other spreading centres.‖. (L17-20 of supplementary) Reviewer #3 (Remarks to the Author): The manuscript tackles a major unsolved issue of mid-ocean ridge research, i.e., the relationship between low-degree of mantle melting and the occurrence of explosive volcanism along the ultraslow spreading Gakkel Ridge in the Arctic Ocean. The authors provide constraints from seismic tomographyrevealing structural elements and numerical modellingindication/simulating potential processes. In concert, both may provide indeed a new perspective on the mechanisms controlling the rather puzzling behaviour of ultraslow spreading ridges, whichfor a long timewere consider to be rather amagmatic and therefore scientists were rather surprised to find explosive volcanism and patches of robust magmatic accretion. In general, I therefore believe that the manuscript can make an important contribution.
However, there are a number of features that need to be improved before the manuscript can be finally evaluated. First, the text und title are still rather -sloppy‖. For example, the title highlights the features to be discussed in the paper, but overall, it's nothing new.

REP:
In our opinion, the statement in the title, which is proven by our results, is not obvious. As far as we aware, the link between -low-degree mantle melting‖ and -explosive volcanism was not explicitly considered by anybody before.
Thus, rocks showing a low degree of mantle melting were sampled years ago. And of coursethe mantle melting is the underlying process that controls features occurring at shallower levellike deep seismicity and occurrence of explosive volcanism. The fact that seismicity shows a very deep level of activity was shown by one of the authors previously (Korger and Schlindwein, Geophys. J. Int., 2012) and also the occurrence of explosive volcanism is well known (Sohn et al., Nature, 2003).
REP: Yes, the information you mentioned was known before. We have just added a few new elements in this puzzle, namely P-S tomography and numerical modeling, that together with the previously known data has allowed us to create a composite picture and to propose some not obvious conclusions.
When reading the manuscript, I'm lost if we really learn something new. Therefore, the authors fail to make their point clearly. However, some of my personal uncertainty about the manuscript comes from the style of writing and how terms are chosen/used. Thus, at several places nonunique geophysical observations from the tomography are presented as supporting a unique explanation.
For example, high Vp/Vs ratios are presented of being a solid fact for melting. Of courseat settings where melts migrate upwards geophysical data often reveal high Vp/Vs ratios. However, also settings with a high degree of serpentinization show high Vp/Vs ratios (Christensen, 2004) and serpentinization is a common process at ultraslow spreading ridges. Further, a fractured rock with fluid filled veins also has a high Vp/Vs ratio (Popp & Kern, 1994;Wang et al., 2012). Thus, it's rather misleading to claim that Vp/Vs provides unique evidence for occurrence of meltingat least in the lithosphere of an ultraslow spreading mid-ocean ridge. (REP: This is not fair. Besides melting, our interpretation also presumes the existence of volatiles, as stated throughout the text. To set this statement clearer, we replaced -partially molten volatile-rich magma‖ with -partially molten and/or volatile rich rocks‖, L20. We mention both melts and volatiles in L105, L119 and others). However, the numerical simulations may suggest that at the depth/location were the tomography finds high Vp/Vs ratios, melts should occur. In this case, the interfingering of simulations and evidence from the seismic tomography would support a new point of view that may indeed merit publication. Unfortunately, the current manuscript isn't making the pointor if it does, it's not well presented. Thus, to really make the paper a manuscript of interest to a broad audience, results from the seismic tomography should be linked in the discussion much more clearly to the features of the numerical model. Further, observation should be presented in a way that alternative interpretations are not ignored (like high Vp/Vs could be either melts, serpentinized rock or fractured and fluid filled rocksor a combination of all).

REP:
We agree that besides melt content, many other factors can affect the seismic velocities and Vp/Vs. Obviously, it is not possible provide a unique interpretation based on only seismic models. Throughout the text, we softened the statements related to interpretation of our model by saying that this is one of possible explanation of the observed structures.
At the same time, we slightly disagree with a possibility to interpret the high Vp/Vs ratio by serpenization instead of melting. Of course, at ultraslow spreading ridges, serpentinization plays a role, but away from such large volcanic centers with fresh basalt at the seafloor and a thick magmatic crust. With the Jasmine cruise and findings at the SWIR, there is growing evidence that the volcanic centres of ultraslow spreading ridges do show a crust that is much thicker than in the adjacent amagmatic regions. In addition, at the Seg8 volcanic complex, for example we found this melt volume based on seismic tomography and high vp/vs ratios and we see a very comparable feature at Logachev volcano on Knipovich Ridge (recently submitted seismic tomography). We don't think that anyone would argue for serpentinization in these regions that show concurrent intrusive activity with migrating earthquake swarms. So we think we need to stress this point more that we see high Vp/Vs ratios immediately below a region that is known to show recent (1999)(2000)(2001) volcanic activity.
Further, the relationship between features found in the seismic tomography and the numerical simulations need to be explored in more detail. In the current version of the manuscript I have sometimes the feeling that the comparison of features is rather incidental (i.e., comparing only one or two depth slices instead of using the geometry of a 3D volume). Thus, to relate the pattern found in the simulations to features found in the tomography, you only used one depth slice at 20 km. What will be needed is to show it in 3D.
REP: Unfortunately, it is not possible yet to set the direct connection between the tomography results and numerical modeling. It is clear that seismic tomography cannot provide unique values of physical parameters needed for modeling due to many reasons (lack of resolution, uncertainty in damping definition, non-unique transition from seismic to petrophysical properties etc). On the other hand, numerical modeling presumes some simplifications that makes impossible to simulate directly all details observed in the nature. Finally, the numerical modeling provides temporal evolution, whereas seismic tomography is an instantaneous snapshot of the current state. Therefore, we can compare seismic tomography and numerical modeling results only qualitatively. In our opinion, demonstration of the correspondence in 2D sections is clearer than analyzing 3D images. Presenting tomography results in 3D is only efficient if there is a possibility of interactive rotation of the model; just static images of the 3D patterns often look non-informative and sometimes misleading.
In summary, I do see a paper with interesting and new results from the Gakkel Ridge, providing great structural images from seismic tomography. Further, numerical simulations are used to yield (some of) the processes controlling the behaviour of mantle melting and thus both datasets together can provide a new and deeper understanding. However, the current paper fails to do it. First, in the introduction the open questions and mysteries of the Gakkel Ridge should be clearly stated, to help readers to understand the aim of the study and why the different approach were used and why they nurture each other. Right now, the aim of the study isn't really stated.

REP:
We have made corrections throughout the text of the main paper to better emphasize the importance of joint using seismic tomography and numerical modeling.
Second, results from the tomography should be discussed more openly. Do not try to -hide‖ that some interpretations might not be unique.

REP:
In the supplementary, we have added a lot of information with the details on how seismic tomography was performed that honestly show the limitations and weak points of our seismic model Third, describe more clearly the features arising from the simulations. To me it's unclear if melt migration is really a part of the output of the modelling or if it is approximated from the other parameters (note -I'm not a modeller myself and thus it should be clear to -dummys‖).

REP:
The modelling results have been described more clearly. Our model simulates melt extraction and propagation in a simplified manner (see Method section). The computed melt trajectories follow the topography of the mantle solidus surface under the lithosphere, which allow melt accumulation in multiple magma chambers that develop in the areas of the highest solidus surface topography (magmatic segments). Numerical results are shown in the Fig. 3. The lowered melt supply associates with strong variations of brittle-ductile boundary depth along the ridge, which therefore breaks spontaneously into narrower and hotter magmatic and wider and colder amagmatic sections. The oval-shaped magma chamber spontaneously forms by focusing of the extracted low-degree melts toward individual melt traps. Melt migrates along the detachment faults in the footwall and normal faults in the hanging wall and then forms new crust and volcanoes through spontaneous cooling and crystallization Last, discuss both approaches in concert and thus show readers why your results are so cool to merit publication in Nature Communication. What's the ground-breaking result? As I iterated aboveall features from the title have been know before. So -why your study and what's the benefit?
Additional comments (mostly taken from the annotated m/s; please note the m/s has more comments and suggestions and I only copied a few into this formal review): 1.) Some of the SP waves in Supplementary Figure 1 show SP waves which have larger amplitudes than P -as expected. However, some have smaller amplitudes. Are those really SP waves or are they some P-wave multiples of sideswipes and not converted S-wave energy? Please provide Wadati plots (or at least one plot combining P-time vs. S-time of all pairs) in the supplement. A Wadati plot of each earthquake should help to define better if picks are indeed appropriate or spurious.

REP:
Wadati diagrams are in this case difficult to use. The concept of the Wadati diagram presumes a model with a constant Vp/Vs ratio, which is obviously not our case. In our model, Vp/Vs=1 in water and is in a range of 1.7-1.9 in the solid ground. Therefore, for a shallow local event, the Wadati diagram will be nearly horizontal. The angle of the diagram would be mostly dependent on the depth and remoteness of the event, and not on the actual Vp/Vs ratio. It would give very strong scattering of the Wadati diagram making it useless.
Furthermore, since the stations drift on sea ice over an area with highly variable bathymetry, a different thickness of the water layer needs to be incorporated into the Wadati plots, requiring some knowledge of the wave propagation paths already. In addition, in quite a few cases, we receive clear P arrivals from all stations but only SP arrivals on one of the 3 arrays, such that a Wadati diagram (requiring at least 2 SP-P/P pairs) cannot be established.
According to this reviewer's comment, we have considerably expanded the description of the initial data processing in L107-125 of Supplementary.
2.) Please also show histograms of residuals of both P-and SP. The quality of tomographic results is rather poorly presented.

REP:
In supplementary, we have added a table S1 with the information about the mean residuals during iterations and some text with the discussion of the observed values (L169-178). According to the reviewer's comment, we have added Figure S2 with histograms of the residuals after the 1st and 4th iterations.
3.) Korger and Schlindwein (GJI, 2014) provided a P-wave tomography from the very same data used in this study. I have to say that the transects from both studies are rather difficult to compare as the strike of depth sections in slightly different. However, Korger and Schlindwein didn't reveal any P-wave anomaly where this study has a strong positive velocity anomaly. Which tomography shall I trust? Rather puzzling and I would like to get a good explanation for the different features steaming from the same data. Considering that travel time data are the same I cannot see why the models should be so much different.

REP:
The distribution of the P-wave velocity anomalies in the new tomography model demonstrates some similar features compared to the previous model by Korger and Schlindwein (2014). At the same time, some changes in the velocity model are caused by considerable improvement in source location accuracy owing to adding the S-wave data.
Korger and Schlindwein (2014) did a first relocation of hypocentres in a 3D velocity model that only incorporated a 3 D bathymetry layer. After that, since FMTOMO can only invert for P velocity, earthquake locations were kept fixed and the P velocity model was determined. In view of much better determined P phases, this seemed an appropriate choice. LOTOS has the ability to invert jointly for S and P velocity structure and apparently can also deal well with data sets that only have limited observations. So this new study is certainly a more complete image of the local structure and given the pronounced difference in vp/vs ratio, a joint inversion and certainly a relocation of the events in a new 3D P and S velocity model is necessary. We have added a few phrases about the comparison of these studies in Supplementary in L162-168.
4.) Why occur some Vp/Vs anomalies with a similar amplitude away from the proposed magmatic conduit (to the north and west)? If it is really magmatic activity causing the anomaly and the activity is linked to the local earthquakes -why have the other anomalies no quakes? Or are these features not so well resolved and hence artefacts? Based on Korger and Schlindwein only the central area had a large number of rays and good coverage. How much bias is caused by rays having longer offsets. For those, the tomography will have a rather low resolution at shallow depth. However, shallow features are important and show generally the largest lateral variations, causing significant delays. How robust is the inversion of deep-seated features when the shallow structure lacks resolution/coverage?

REP:
We have added some new synthetic tests with free-shaped anomalies to see the robustness of the anomalies in different parts of the study area. It can be seen that the high-amplitude anomalies in the western margin of the area are not correctly resolved. Therefore, according to the results of these tests, we masked the poorly resolved areas in the main results. Regarding the deep-seated anomalies, we have designed a special test in Figure S7 to assess their stability. We have added the descriptions of these tests in L226-249.

5.)
Please discuss what is the origin of the other Vp/Vs anomalies? Melts, too? Fracturing?

REP:
We admit that the numerical values of anomalies strongly depend on many different factors, such as uneven resolution and uncertainty of damping definition. Therefore any attempts of direct conversion of seismic parameters to temperature, melting, composition and other petrophysical parameters are very risky. Therefore, we insist that the results of seismic tomography in most cases can be interpreted only qualitatively. It should be noted that our resulting distribution of Vp/Vs looks similar to the results of tomography inversions for other active volcanoes in the world, which allows us to make some extrapolations. We have added a paragraph with the discussion of this issue in the main article in L105-113.
6.) The swath mapping had a rather limited coverageonly at the centre of the study area. How was the seafloor depth constrained where no swath data exists? From IBCAO2 bathymetry? In this case ray entry points into the seafloor might be biased as the seafloor is often based on interpolated data and not measured soundings, in turn, causing significant delays and hence limiting the resolution power of the tomography.

REP:
For calculation of travel times, we used lower resolution regional model presented in Figure 1c. It is true that using this oversmoothed model may cause some bias of travel times. On the other hand, some natural averaging occurs due to finite frequency content of the arriving waves. For example, for periods of 0.2-0.5 s and velocity 5-7 km/s, the wavelength would be in the range of 1-2 km. Therefore, the conversion of seismic waves